When I applied for a PhD student position I had an interview with two professors. Somehow we touched the problem if $P$ is $NP$ and, once we got there, for some reason both professors made it clear that in their opinion there is absolutely no point attacking such a hard problem. Of course this is the case for a starting student, it is more fruitful to build the basis first. But they basically stated that the problem has been studied by so smart researchers that no mortal could do better anyway.

This makes me wonder should one attack such hard problems at all? If one should, why and when? Will studying hard problems span new ideas? Is it even a necessity to understand some hard problems and, especially, why they are hard to solve? Or is it just pure waste of time? Or is it that one should learn some hard problems to educate oneself but not spend time attacking them?

I'm not sure this is an ideal MO question because it doesn't have a unique answer, it just has people's opinion. But here's my opinion. I've supervised over 10 PhD students to completion and one thing I know is that if you give a PhD student a problem for which there is a non-zero chance that after 4 years they have done nothing worth publishing (e.g. because the problem has been studied for so long by so many people that 4 years isn't enough), then you have just ruined that person's math career. On the other hand, at least once a month I try to work on a famous unsolved problem for a bit.
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user30035Feb 27 '13 at 7:42

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I've never heard of anyone accidentally solving a hard problem. Trying is at least a necessary condition. How to go about it and which problem to pick, that's a different matter.
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JBorgerFeb 27 '13 at 8:51

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Well, this is just because I was not yet active on MO then ;) Kidding aside, on the one hand it is really true that earlier in the sites history there was a higher tolerance, yet on the other hand and more importantly it also depends on the precise nature of the question. This one is way too vague in my opinion. What's a 'hard problem' even? You mention P vs NP and what else. If you want to start a more detailed discussion please create a meta thread, link at the top, extra signup necessary but easy and instant.
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quidFeb 27 '13 at 14:06

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This question has been closed and currently has 3 votes to reopen. Before the comments get out of hand here, I wanted to have a meta thread. Please upvote this comment so it appear above the fold and please carry discussion of whether this should be open or closed to: tea.mathoverflow.net/discussion/1546/…
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David WhiteFeb 27 '13 at 14:19

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The simple advice (for an academic mathematician) on whether to work on a hard problem: "Not until after you are tenured."
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Gerald EdgarMar 11 '13 at 13:58

7 Answers
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1) You have a fair evidence that you are strong enough to tackle things other clever people gave up on. The evidence should be tangible. The best evidence is, of course, having solved at least one hard problem already, but that, obviously, cannot be applied to your first hard problem ever. Sometimes a good indication is other people saying something like "You should stop stealing other mathematicians' daily bread and do some real thing that no one else can do!" (Note that you shouldn't follow the first part of this advice.)

2) You have an escape strategy. That may be thinking of something else in parallel, making sure that your plan is such that even a partial progress can be of value, etc.

3) You are not afraid to fail and are used to the feeling of being a hopeless idiot (meaning you can calmly admit this frustrating fact about yourself without any reservations, excuses, or other kinds of self-deceit and still push ahead at your full strength).

4) You have enough free time and do not care too much of your career ups and downs.

5) You are sufficiently open-minded to see things at unusual angles and are trained to figure out reasonably quickly whether any given idea may possibly work or it certainly won't. Note that both are tough skills, which are almost completely untouched in most standard treatises on problem solving.

6) You love the problem. This should, actually, be #0 rather than #6, and it is hard to explain what it means in rational terms, but you can feel it when it happens.

If those conditions are satisfied, go ahead and try shooting the Moon. If not, you'd better make your way up slowly step by step like most of us, picking the fight just slightly bigger than your own size every time.

I'm not a great believer in "having a new idea from the start". The new idea or a combination of ideas usually comes eventually when working on the problem and the moment it comes is often very near the end of the story. The trail of failures that precedes it is well-hidden, but we all start with "I have no method, no feeling, no tools, no clue, and no hope" and proceed through "twisting this, we can get a bit more or something a bit different, however the main difficulty remains untouched". You have to figure out not only what doesn't work but also how exactly it doesn't work. Most of the time is spent on constructing examples and counterexamples to the steps in your initial plan, digressing into simpler models, checking that no information is lost at each particular step, i.e., that if the original theorem is correct, then the intermediate lemma you want to try is at least very plausible, and so on, and so forth. I do not know how it works for others, but for me any non-trivial problem is a scattered jigsaw puzzle, not an originally blurry but complete picture I merely need to focus the camera on.

I'm not sure how much credibility I can claim myself when talking like this about solving hard problems, but, fortunately, most of these claims aren't my creations: I merely believe they are true and the opposites are false. So, take all this with a healthy grain of salt and keep in mind that out of 100 mathematicians, at most 5 are qualified to shoot the Moon in principle and, out of those 5, at most 1 will score a hit when making this long shot, so don't judge us, professors, too harshly when we just know our limitations and are unwilling to try to jump above our heads. There is a lot of stuff at the knee level that needs to be done and some of us (including myself) just feel that it will be more efficient to spend most of our time doing it there. One becomes a loser not when he aims and shoots lower than the Moon but when he stops seeing it in the sky :).

As to the formal question list, I would answer as follows:

Should one attack such hard problems at all?

Yes. The gods won't do it for us, so it'll have to be one of us, poor mortals, who should try.

If one should, why and when? See #1-#6 for "when". As to "why", if one asks this question, one shouldn't.

Will studying hard problems span new ideas?

Possibly. It can work out either way.

Is it even a necessity to understand some hard problems and, especially, why they are hard to solve?

No, nothing is absolutely necessary. You can live and work perfectly well without it.

Or is it just pure waste of time?

This depends on who and what you are.

Or is it that one should learn some hard problems to educate oneself but not spend time attacking them?

Here is what both Feynman, Grothendieck (and my father) said: have several projects in mind at all times.

Grothendieck explains a two year state of depression he went through at the beginning of his career to the fact he single mindedly followed one goal which turned out to be very illusive.

Feynman explained his success on the fact that the he always had several questions in his mind and kept an open eye for anyting that might relate to this. That is why he found attending seminars so much more helpful.

As for successful PhDs dissertations I read somewhere, long ago, that there are of two types

the type where you find a new method for an old question,

and

the type where you find a new question for an old method.

Statistically, the 2nd type is more prevalent. Obviously that is a rough classification and dissertations are cocktails of both types.

So to answer your question, should you try to solve hard problems, my answer is yes, but remember that, even if you do not get the whole dinosaur in you dissertation, his tail may be good enough to make you a Doctor in Sciences.

As a grad student who is close to finishing his PhD, I am probably not qualified to really discuss one's career as a research mathematician. However, at this moment I disagree with this answer. I've worked on many problems during my graduate career (partially because I earned a masters in computer science on the side) and what I found was that I could only focus and do good work on one problem at a time. Perhaps this will change over time, but especially for a young mathematician my advice would be to focus on one thing, get the degree in hand, get a job, and later on broaden your focus.
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David WhiteFeb 27 '13 at 14:25

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In particular, because research is hard and it's also hard to discipline yourself to write things down as you go, I feel like having too many problems can distract you from what's important or from completing a project. Again, this may change as you get older, and I hope it does. For now I've learned the hard way to keep my new ideas in folders for future projects but to only work on one at a time until the preprint is done.
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David WhiteFeb 27 '13 at 14:26

When thinking about attacking a hard problem one should ask: Do I have a tool or an idea that other people who attacked the problem did not have? If so, one should give it a try. If not, one will be most probably not better than others.

"Inspiration exists, but it has to find you working." P. Picasso :-)
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Francesco PolizziFeb 27 '13 at 10:52

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Problem is that often failed attempts don't get published thus its hard to say what has been tried without success.
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user10891Feb 27 '13 at 11:04

@Frank: But you can often see that a method is new. Examples are Andrew Wiles' use of elliptic curves for Fermat's problem or Heinrich Heesch's idea of using computers to attack the Four Colour Problem.
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remFeb 27 '13 at 13:18

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@Markus: IIRC Wiles was not the originator of the connction between elliptic curves/modular forms and FLT
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Yemon ChoiMar 11 '13 at 10:04

Yes, but he started to work at the problem when it became known that there was a connection. At this point he knew that he had an approach that earlier researchers had not.
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remMar 11 '13 at 11:11

I think Markus Redeker's answer captures the essential point. If the problem is hard and famous (at least in the relevant sub-field), so a fortiori for a problem like P≠NP, I would add the further restriction then you should consider attacking it only if that new idea you have allows you to solve an easy or average (but still new) related problem or at the very least allows you to reprove in a completely different way a known result. If this works, then 1) you now know that this new idea is not completely crazy or just a variant of an old one 2) you have a worthy PhD. 3) you can think about making math history. In fact, if you skim through math history, recent or otherwise, you will see that because of point 1) (testing that you idea is indeed new and worth pursuing) many historical breakthroughs were preceded by an easy (or at least much easier) variant relying on similar techniques.

As I understand, you are only beginning your graduate studies.
At this stage you should get a problem from your adviser, a problem that you are likely to solve.
If you want to become a professional mathematician, you should publish regularly, and for this
you need problems which you are likely solve in reasonable time.
What kind of problems you are likely to solve, you will gradually learn from experience.
But in the very beginning, rely on the experience of your adviser.

But of course, you should also learn about "big and famous" problems, and think about them too.
Then, if you are lucky, you have an idea how to make a progress in one of them.

My main advise for the beginner: choose a right adviser, and do what s/he recommends.
In the remaining time, read and think on other problems.

That if one can not solve a hard problem, then solve a similar but easier problem. I like thinking about the hard problems in my field, knowing that it doesn't take tons of creativity to solve something easier after seriously studying those.